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Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: Twitter: Dereklowe

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February 11, 2011

Drug Problems: A Diagnosis

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Posted by Derek

There's no shortage of "What's Wrong With the Drug Industry" article these days. I wanted to call attention to another one that's just appeared in JPET. I don't agree with all of it, but it does make some important points.

If I had to give a one-line summary of its thesis, it would be "Drug discovery forgot pharmacology and lost its way". The author, Michael Williams of Northwestern (and of 35 years at Merck, Novartis, Abbott, and Cephalon) is a pharmacologist himself, and feels that the genomics era (and indeed, the whole target-driven molecular biology era) has a lot to answer for. He also thinks that people have become seduced by technology:

Rather than creating synergies by using multiple complementary
technologies to find answers to discrete questions in a focused and coherent manner, technology-driven drug discovery has become a discipline that justifies its existence by searching for questions. An example of this is the proteomics approach to target validation, where the intrinsic complexity of the protein component of a cell or tissue necessitates a reductionistic approach where experimental samples must be separated into bins to facilitate analysis with timelines for data generation that can stretch into months or years.

To those with a technology bent, new iterations on a technology, regardless of its utility, inevitably become “must haves,” with acquisition and implementation becoming ends unto themselves. . .

One place I disagree with him is in his assertion that "Implicit in the HTS/combinatorial chemistry paradigm was/is that each target was equally facile as a starting point for a drug discovery project". That hasn't been my experience at all - there's always been a lot of arguing about which targets should be taken to screening and of what kind (how many GPCRs versus enzymes versus what-have you). Williams makes his point in the context of the genomics frenzy, when it was thought that all kinds of targets would be emerging. But at least where I worked, the hope was that genomics would provide a lot of good, tractable target that we hadn't known about, rather than just a long list of orphan receptors and whatzitases. (Mind you, that list is exactly what we ended u with).

Williams then discusses the problem of whether some targets are, in the end, truly intractable. The "just one more whack at it, and we'll get there" approach sometimes works, but it does try the patience:

Drugs active at opioid receptors remain the gold standard of analgesic care and include morphine, codeine, and oxycodone. With the discovery of the mu, delta, and kappa receptor subtypes in the 1970s, it was anticipated that development of selective agonists for these receptors would result in drugs that had a reduced liability for the respiratory depression, tolerance, constipation, and addiction associated with classical opioids. Some 40 years later, despite considerable efforts in medicinal chemistry and molecular biology to refine/define the structural characteristics of receptor-selective NCEs, the ”holy grail” of side effect-free opioids appears as elusive as ever, with a multitude of compounds showing compelling preclinical data but failing to demonstrate these properties in the clinic. . .

Another of his examples in this line are the muscarinic ligands, which I know from personal experience, as a search of my name through the literature and patent databases will show. And although GPCRs are among the most valuable target classes of all, we still have to face up to some disturbing facts about them:

Thus, for both of these G protein-coupled receptor families, a major question is whether their function is so critical, nuanced, and complex as to preclude advances based on the molecular approaches currently being used that may lack the necessary heuristic relationship to the complexity/redundancies of the systems present in a more physiological or disease-related milieu. Based on progress over the past 40 years, it may well be concluded that the opioid and muscarinic receptor families represent intractable targets in the search for improved small-molecule therapeutics. But maybe the next NCE….???

At the end of the article is a table of possible approaches to get out of the preclinical swamp. Interestingly, it's noted that it was "generated at the request of one of the reviewers", who probably asked what the author proposed to do about all this. I won't reproduce it all here, but it boils down to being more rigorous about data and statistics, using the hardest, most real-world models, and giving people the time to pursue these approaches even if they're going against the crowd while doing so. I don't see any his recommendations that I disagree with, but (and this isn't his fault), I don't see any of them that I haven't seen before, either. There needs no ghost, my lord, come from the grave, to tell us this.

Comments (23) + TrackBacks (0) | Category: Drug Development | Drug Industry History


1. PharmaHeretic on February 11, 2011 10:41 AM writes...

Any comments on this article? It kinda makes sense in that a few dozen genes (products + silent) could be behind the cancer phenotype, but there can be thousands of ways for the cell to lose regulation on these genes.

Cancer resembles life 1 billion years ago, say astrobiologists

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2. CMCguy on February 11, 2011 11:29 AM writes...

I do believe much of the current "unproductivity" in Pharma is partly due to companies in past couple decades being "seduced by technology" with variety of diffrent ones that came along. The many fads were (over)sold as faster and easier means to supplant drug discovery rather than augmentation of efforts (which most became). The chase was about numbers (Targets, compounds, NCEs, Market size) without enough considerations on quality or viable drugs/treatments. I can't totally blame these distractions on MBA types who grasped as simpler and cheaper replacements because many in R&D held to certain things being the way to go and ignoring the fact that typically new technologies addressed only portions of the drug development puzzle and in solving certain problems would create others unless applied some of the lessons from more traditional routes.

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3. milkshake on February 11, 2011 12:35 PM writes...

I think the root of pharma unproductivity is in the change of industry culture from research-based to finance-centered. Industry got victim of its own success: the double digit returns in 80s and 90s convinced investors that pharma is a better investment than defense industry. Introduction of new drugs got a lot more expensive but successful drugs got a far more profitable too hence the attempts to repeat such success leading to blockbuster mentality.

I think a far bigger problem than technology fads were the massive short-term gain incentive schemes for top management previously common only to finance sector which were totally conterproductive for pharma industry. The obscene rewards also brought in more corporate types from law a finance and this influx changed the corporate culture.

Further, the huge and increasing costs of development and the longer research-to-profit lead times gave huge advantage to largest corporations. Underperforming companies with idiotic management were able to sustain themselves by swallowing their competitors - by promising that the merged organisation will have a better long-term productivity and lower cost. While the improved productivity never materialized, the merger cost had to be offset by massive cuts somewhere and research turned out to be especially vulnerable because cutting research does not have immediate effect on profitability. The incessant job cuts and reorganizations then had a disastrous effect on motivation of people in research.

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4. NoDrugsNoJobs on February 11, 2011 12:38 PM writes...

I would agree with this as well. I remember when a large pahrma I was with decided we had to automatically assess all compound properties (solubility, etc) and an entire group was set up to do this. The problem was that by the time we got the results back from this automatic preclinical assessment, we had already gone on to characterize the compounds in vivo. The reality was that we were getting all the information we needed at that point and while the profiling tools were nice to have available if you did run into a specific problem where you needed to track down to one of these variables, the size and importance of this profiling group took on its own life and significance including lots of money and resources and additional beareucracy. Lots of stuff like that in big pharma - its like every technology became must have and then we medchem guys would have to try to present our discoveries in a way where we would bring in how all these technologies were incoroprated into our molecule's discovery when most of the time that just wasn't the case. Give me a good medchemist that can both make a compound and understand the pharmacology in the area to the point where their instincts are sharply honed and I will give you a team that has a chance. Give me an automaton following some preset discovery paradgmn and I give you a much lower and more expensive chance of success. Just sayin....

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5. Dr Jimbo on February 11, 2011 12:41 PM writes...

It kinda pains me to say it, but that's an excellent critique of proteomics. No matter how impressive the capabilities of any new technologies are, they're no use if they don't bring you closer to your goal.
I can understand somewhat how scientists may be seduced by the shiny new system and it's impressive results, but why would the fabled MBAs be impressed by the ability to detect attomoles of proteins or whatever it might be.

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6. Virgil on February 11, 2011 12:42 PM writes...

One thing I do see happening with technology, which is "going against the grain" is the more recent adoption of HTS by academia. Unlike proteomics which sort of developed hand-in-hand in industry and academia, HTS was until very recently the sole preserve of industry and was completely inaccessible to anyone in a University setting. Now though, libraries are easy to get, and we're finally seeing (e.g. in the pages of Nature Biotech,) some really nice phenotypic screens happening in whole cells. The hope would be that maybe academia, with better designed screens, can succeed where industry failed. Of course, it will take a loooong time.

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7. emjeff on February 11, 2011 1:29 PM writes...

The late David Horrobin said much the same thing in a 2003 article in Nature Rev. Drug Discovery. In addition to calling for more whole animal work (going against the grain of today's reductionism), he also called for a revival of the discipline of clinical pharmacology.

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8. Andy on February 11, 2011 1:38 PM writes...

Re: HTS in academia:
Unfortunately, in the US the rate limiting step is poor priority scores given to high throughput screening proposals by NIH reviewers since HTS experiments are "fishing expeditions", "not hypothesis driven" and "fail to provide mechanistic insights". I speak from direct experience here.

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9. Bunsen Honeydew on February 11, 2011 2:59 PM writes...

Gotta agree 100% with Milkshake on this one. The slide began when the MBAs took control of pharma from the PhDs and I don't think that's a coincidence.

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10. MoMo on February 11, 2011 3:21 PM writes...

Don't forget the legions of biology Ph.D.s studying the subject because its easier than studying chemistry! A 10 to 1 ratio.

Now Pharma is paying the price and even chemists are classified into doers and talkers-i.e actual synthetic chemists vs. the "designers"

Time for a revolution whereby the Chemists fight back!

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11. Medicamenta Vera on February 11, 2011 4:46 PM writes...

Dear Momo:
Don't know what planet you work on, but at the companies I worked at the med chem to pharmacologist ratio was usually >1 but

There is plenty of blame to go around, especially the med chemists who went into upper management.
That said, Phase II failures would seem to be a significant contributor. There are quite a number of anti-inflammatory and cardiovascular drugs that worked spectacularly in animal models and were duds in the clinic.

One approach that might improve the odds is to do less animal disease model pharmacology in preference for pharmacodynamic SAR work (i.e., what really hits the target in vivo). Demonstrating efficacy in animal models, I believe, doesn't "de-risk" a target, adds to timelines, and may make you discard promising targets.

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12. Medicamenta Vera on February 11, 2011 4:48 PM writes...

Dear Momo:
Don't know what planet you work on, but at the companies I worked at the med chem to pharmacologist ratio was usually >1 but less than 2.

There is plenty of blame to go around, especially the med chemists who went into upper management.
That said, Phase II failures would seem to be a significant contributor. There are quite a number of anti-inflammatory and cardiovascular drugs that worked spectacularly in animal models and were duds in the clinic.

One approach that might improve the odds is to do less animal disease model pharmacology in preference for pharmacodynamic SAR work (i.e., what really hits the target in vivo). Demonstrating efficacy in animal models, I believe, doesn't "de-risk" a target, adds to timelines as well as compound requirements, and may make you discard promising targets.

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13. Hap on February 11, 2011 5:44 PM writes...

There are a lot of bad animal models, but don't people not yet understand what targets correspond to what disease states? Making sure your drug binds to target is helpful only if you know the target means something.

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14. JasonP on February 11, 2011 6:26 PM writes...

Lets review why pharma is failing lately:

1. The HTS mindset reality has been applied to too many steps of an inherently byzantine process.

2. The acquire and gobble efforts of various companies have succeeded more in breaking up great scientific teams and stifling innovation than advancing drugs.

3. The new kleptocracy economic model that is taking hold of American capitalism day by day just as in Russia.

I think there is one more important point:

4. 2000-2010 was dedicated to discovering how complex and redundant biology really is. Even today people are still obsessed with the silver-bullet-one-molecule method of curing a disease, when it seems patently obvious to me that you need a molecule soup to trigger the correct biological machinery to ameliorate disease.

The cure: get back to basics and the reality that there is no replacing old fashioned, thorough scientific discovery.

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15. Charlie on February 11, 2011 7:29 PM writes...

There is no solution to fixing bloated stock prices due to massive accounting fraud. Wait for the inevitable collapse of the US dollar and start anew.

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16. Charlie on February 11, 2011 7:36 PM writes...

Modern bioscience requires a chemist, physicist, mathematician, and biologist rolled into one human being. What ever happened to all the interdisciplinary hype? Oh I know, that would require lifetime employment in one career and the criminals in the kleptocracy don't like that. A real shame for humanity.

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17. Mutatis Mutandis on February 12, 2011 7:38 AM writes...

Fully agree with (16), with the modest correction that is sufficient for a team of four people to include a cell biologist, a molecular biologist, a chemist, a physicist, a statistician, a structural biologist, an IT person, an accountant and a project manager. What illustrates the risk, IMHO, of always trying to hire specialists who are top-notch in their particular field.

The objection against technological solutions is fair enough -- and I speak very much as a "technology person". The problem is that the managers of the pharmaceutical industry have been seduced by an endless series of "silver bullets" that promised to solve the problem for them, instead of working hard to integrate all practical means in a scientifically valid approach. To paraphrase Monty, we always seem to aim a bridge too far.

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18. Still Scared of Dinosaurs on February 12, 2011 11:02 AM writes...

The giveaway for me has always been the structure of the Clinical Study Report (CSR). 8 sections of blah blah followed by baseline characteristics and study conduct; then efficacy; then safety; then conclusions.

Most teams don't even know where to put the clinical pharmacolgy so they stick it at the end of efficacy. Putting it at the end of section 9 makes more sense but instituting a separate section would be optimal.

Of course I also think that, in general, measuring PK in Phase 3 is an admission of failure. But if you characterize the dose->PK->PD relationship earlier you should be able to make sense of the dose->PD->effect relationships in the larger populations.

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19. Kling on February 12, 2011 1:05 PM writes...

Has it occurred to anyone that drug discovery follows an S shaped curve, and there are chemical/biological limitations on what can be cured in a cost effective way?
Part of the problem comes from our brand of scientific rationalism that makes us think there is always a therapeutic out there better than what we got.

Maybe, maybe not. I wonder where the legion of hammer and screwdriver makers went after their thousand years quest of making more potent hammers and screwdrivers.

We should seriously entertain the notion that big time drug discovery may be dead. After all, therapies are measured against standard of care. This is an asymptote. What if the standard of care is already the best we can do?

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20. RB Woodweird on February 14, 2011 7:37 AM writes...

I agree with the author's point, but his writing style makes my head hurt.

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21. Jonathan on February 14, 2011 9:07 AM writes...

@Momo - I don't agree. Mostly as a consequence of the MBA problem identified by Milkshake, it seems that Pharma has lost touch with the underlying biology of the diseases its trying to treat. If you don't understand the disease, is it any wonder the drugs don't work?

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22. Torsten on February 15, 2011 3:21 AM writes...

Has genomics fared as badly as many assume? An interesting counterpoint from Nat. Rev. Drug Disc. (Dec. 2010) in a correspondence by Hall et al entitled "Genomics drugs in clinical trials" suggests that genomics has made a more significant contribution than is often credited. The closing sentence is quite apt:

"Although genomics technologies are not substitutes for hypothesis-driven disease biology, medicinal chemistry and clinical testing, they have become firmly embedded in the drug discovery process and it seems likely that many more drugs in the foreseeable future will be genomics drugs."

Sure genomics has been over-hyped but there is now a clear danger that the pendulum has swung too far the other way and its potential is being missed.

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23. Anonymous on February 15, 2011 3:46 AM writes...

Some good comments here. I especially liked yours, @milkshake. Did you work at GSK? Your comment is an uncanny critique of everything that was and is wrong that particular WindPharm!

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